Determine whether the study is experimental or quasi-experimental; describe how you know.

Based on the experimental or quasi-experimental study you researched  for the library search assigned in your studies for this unit, address  the following:

  • Determine whether the study is experimental or quasi-experimental; describe how you know.
  • Describe the variables, both independent and dependent, used in the research.
  • Describe the treatment conditions of the experimental group. If  the study is quasi-experimental, describe the different groups or  conditions that were compared.
  • Describe the specific type of research design that was used, and  discuss why it is considered experimental or quasi-experimental.
  • Evaluate the scientific merit of the selected design. How might  you have designed this study differently? Evaluate how well the  experimental approach and design helped the researcher answer the  research questions.
  • List the persistent link for the article. Use the Persistent  Links and DOIs library guide, linked in the Resources, to learn how to  locate this information in the library databases.
  • Cite all sources in APA style and provide an APA-formatted reference list at the end of your post.

    ORIGINAL PAPER

    A Quasi-Experimental Evaluation of the Impact of Public Assistance on Prisoner Recidivism

    Jeremy Luallen1 • Jared Edgerton1 • Deirdre Rabideau1

    Published online: 12 May 2017 � Springer Science+Business Media New York 2017

    Abstract Introduction The Welfare Act of 1996 banned welfare and food stamp eligibility for felony drug offenders and gave states the ability to modify their use of the law. Today,

    many states are revisiting their use of this ban, searching for ways to decrease the size of

    their prison populations; however, there are no empirical assessments of how this ban has

    affected prison populations and recidivism among drug offenders. Moreover, there are no

    causal investigations whatsoever to demonstrate whether welfare or food stamp benefits

    impact recidivism at all.

    Objective This paper provides the first empirical examination of the causal relationship between recidivism and welfare and food stamp benefits

    Methods Using a survival-based estimation, we estimated the impact of benefits on the recidivism of drug-offending populations using data from the National Corrections

    Reporting Program. We modeled this impact using a difference-in-difference estimator

    within a regression discontinuity framework.

    Results Results of this analysis are conclusive; we find no evidence that drug offending populations as a group were adversely or positively impacted by the ban overall. Results

    apply to both male and female populations and are robust to several sensitivity tests.

    Results also suggest the possibility that impacts significantly vary over time-at-risk, despite

    a zero net effect.

    Conclusion Overall, we show that the initial passage of the drug felony ban had no measurable large-scale impacts on recidivism among male or female drug offenders. We

    conclude that the state initiatives to remove or modify the ban, regardless of whether they

    & Jeremy Luallen jeremy_luallen@abtassoc.com

    Jared Edgerton Jared_edgerton@abtassoc.com

    Deirdre Rabideau Deirdre_rabideau@abtassoc.com

    1 Abt Associates, 55 Wheeler St., Cambridge, MA 02451, USA

    123

    J Quant Criminol (2018) 34:741–773 https://doi.org/10.1007/s10940-017-9353-x

    improve lives of individual offenders, will likely have no appreciable impact on prison

    systems.

    Keywords Welfare � Food stamps � Drugs � Ban � Prison � Recidivism

    Introduction

    In response to the growing financial and social pressures of mass incarceration, policy-

    makers are evaluating policies and practices in the criminal justice system and searching

    for ways to reduce correctional burden while protecting the public interest. One policy that

    has drawn recent attention is the drug felony ban on food stamp benefits (now called the

    Supplemental Nutrition Assistance Program or SNAP) and cash assistance (known as

    Temporary Assistance to Needy Families or TANF). Originally introduced in 1996 as part

    of the Personal Responsibility and Work Opportunity Reconciliation Act (PRWORA), this

    ban completely denied SNAP and TANF eligibility for ‘‘individual(s) convicted (under

    federal or state law) of any offense which is classified as a felony… and which has as an element the possession, use, or distribution of a controlled substance.’’

    At the time it was passed, proponents of the ban criticized drug felons for receiving

    public benefits despite having broken the nation’s drug laws and argued for denial of

    benefits on the basis of moral and social principles (Godsoe 1998; Allard 2002).1 In years

    since, critics of the ban have argued that denying benefits creates a net harm to society,

    worsening outcomes for needy populations and especially for women and children (Mauer

    and McCalmont 2013; Godsoe 1998; Allard 2002; Eadler 2011). Importantly, the original

    law gave states the ability to opt out or modify their use of the ban through legislative

    reforms.

    This feature is important because it suggests why legislators still care about the ban

    today; states across the country are increasingly viewing removal of the ban as a way to

    reduce the number of drug offenders returning to prison after they are released. For

    example in 2014 and 2015, Missouri and California (respectively) enacted new laws that

    completely or partially removed the SNAP ban for convicted drug felons. Similarly, in

    2015 the Alabama legislature passed a prison reform bill that allows drug felons to start

    receiving benefits in 2016 (Edgemon 2015). These illustrations are telling—the high costs

    of prisons and changes in social and political attitudes towards the ban are driving its re-

    examination.

    Despite the political rhetoric surrounding the use of the ban, there is no direct empirical

    evidence to support or reject whether states can measurably affect prisoner recidivism or

    the size of prison populations through their use of the ban. In fact, there does not appear to

    be any causal evidence whatsoever to demonstrate that the receipt of TANF or SNAP

    benefits does or does not have an impact on an individual’s propensity to return to prison.

    This paper investigates the relationship between receipt of public assistance (specifi-

    cally, in the form of SNAP and TANF benefits) and recidivism by examining how the

    enactment of the drug felony ban impacted recidivism rates for drug offending populations.

    Using individual-level prison records from the National Corrections Reporting Program

    (NCRP) across six states, we estimated the impact of the ban’s 1996 implementation on

    1 In fact, the ban itself was a relatively obscure provision in a much larger piece of legislation. Congres- sional records show that the ban provision saw\2 min of total debate (Mauer 2002; Petersilia 2003).

    742 J Quant Criminol (2018) 34:741–773

    123

    rates of returning to prison. We defined a return to prison as a return for any reason

    (conviction or revocation) and for any type of crime.2 Impacts were identified using

    difference-in-difference estimation within a regression discontinuity framework, and were

    estimated through survival-based regression modeling techniques (i.e., proportional haz-

    ards models) described in subsequent sections.

    Overall we find no strong evidence to support the claim that recidivism rates or the size

    of prison populations has been materially influenced by the drug felony ban. Among both

    male and female prison populations, the estimated pooled impact of the ban is not sta-

    tistically different from zero (with point estimates very near zero). Across states, estimates

    are more variable; however, for both male and female prisoners, state estimates provide no

    consistent depiction of how these populations are affected by policy changes.

    Results are also extremely robust to alternative model specifications. We test the sen-

    sitivity of our results to more flexible time trends and alternative parametric specifications

    and find no meaningful changes to baseline results. This implies that changes to drug

    felony ban implementation cannot materially influence the size of prison populations in the

    aggregate.

    We discuss potential explanations for this null finding later in the paper. One of those

    possible explanations, which we explore empirically, is that impacts may be heterogonous

    with respect to time-at-risk. If true, then local average treatment effects could be zero while

    treatment effects within the sample vary. We tested this by stratifying estimates by time-at-

    risk (using 6- and 18-month intervals). From this test we find evidence suggesting that

    denying benefits may in fact improve short-term outcomes while worsening long-term

    outcomes. At the very least, we see this evidence as motivation for future study.

    The remainder of this paper is organized as follows. First, we present a background

    discussion on the role of public assistance in re-entry and features of the drug felony ban.

    Next, we describe the data we use for this analysis and our methods for identifying

    impacts, followed by a presentation of results. We conclude with a discussion of the

    limitations of our analysis and closing remarks.

    Background

    Offender Re-Entry, Economic Challenges and Use of Welfare

    There is a large body of research devoted to understanding how offender outcomes are

    shaped by the economic challenges they face after prison (e.g., Western et al. 2014; Travis

    2005; Petersilia 2003). The reason is that offenders, like other low-income populations, are

    economically disadvantaged and in need of services that can mitigate barriers to successful

    re-entry. Employment is one of the most oft-studied outcomes (e.g., Kling 2006; Bushway

    et al. 2007; Stoll and Bushway 2008), though other economic considerations such as

    housing, court-imposed sanctions (fines, restitution and fees), use of public assistance and

    demand for health services also receive significant attention in the literature (e.g., Sheely

    and Kneipp 2015; Lindquist et al. 2009; Evans 2014; Geller and Curtis 2011).

    2 Since the NCRP does not capture alternative measures of recidivism (e.g., rearrest, reconviction, incar- ceration in jail, etc), we could not explore alternative definitions in our analysis. However, return to prison is a useful and important measure (e.g., Hunt and Dumville 2016; Langen and Levin 2002; Durose et al. 2014). It is often used as a metric for evaluating programs, assessing trends and gauging impacts for other correctional issues of interest, often in concert with other metrics such as rearrest or reconviction (e.g., Bales et al. 2005; Spivak and Damphousse 2006; Steurer and Smith 2003).

    J Quant Criminol (2018) 34:741–773 743

    123

    Two specific public assistance programs, SNAP and TANF, provide significant supports

    to low-income households and families in general, though their use among offending

    populations in particular is unclear. On a national scale, benefits paid by SNAP each month

    in FY2014 averaged roughly 5.8 billion dollars over 46 million individuals, or $125 per

    person per month (US Department of Agriculture 2017). For TANF, FY2014 benefits paid

    each month averaged $2.6 billion dollars (including both federal and required state

    spending) over 3.9 million recipients, or around $667 a month (US Department of Health

    and Human Services 2016). This level of support suggests that both programs may provide

    an important level of assistance to offenders as they re-enter the community. In addition to

    simple subsidy support, TANF assistance can also include a variety of services that may

    further promote successful reintegration such as job training, counseling and crisis

    management.

    Despite its likely importance to offenders, receipt of public assistance and its impact on

    re-offending in the post-release period is an issue we know surprisingly little about. This is

    not because the issue is unimportant or has been overlooked. Rather, there is a fundamental

    lack of data sufficient to study the issue. Few data sources exist which tie together welfare

    receipt and longitudinal outcomes with incarceration, criminal history, and other criminal

    measures (Sheely and Kneipp 2015; Butcher and LaLonde 2006; Holtfreter et al. 2004).

    Even the most basic statistics are difficult to find. For example, we were unable to locate

    any national estimates of how many released offenders receive public assistance including

    SNAP or TANF.3 Overall, the limit to our knowledge at present appears to be this: likely

    somewhere between 25 and 40% of female prisoners are eligible for SNAP and/or TANF

    after release; for males this number is likely between 10 and 20% (Lindquist et al. 2009;

    Lattimore et al. 2009; Ekstrand 2005; Allard 2002; Butcher and LaLonde 2006; Hirsch

    1999). These estimates are both crude and imprecise. They are also evolving as we learn

    more. For example, a recent longitudinal study of prisoners released in Boston suggests the

    likelihood of receiving benefits increases significantly over time, and that welfare receipt in

    the post-incarceration period may be as high as 70% (Western et al. 2014).

    Despite the general lack of empirical data on SNAP/TANF participation and program

    impacts for offending populations, there are many studies that have examined program

    impacts on employment, household structure and household earnings, housing and food

    security and health for participants more broadly (e.g., Blank 2002; Schoeni and Blank

    2000; Lindner and Nichols 2012; Bitler 2014). Evidence from this literature suggests that

    programs like SNAP and TANF can and do have positive impacts on the lives of indi-

    viduals in many cases. In that case, it seems reasonable to assume that offending popu-

    lations enjoy similar benefits from participation. For these reasons, scholars have argued

    that ‘‘an offender’s eligibility to receive public assistance is critical to successful reinte-

    gration’’ (Petersilia 2003).

    SNAP, TANF and Recidivism: The Potential Impact of Denying Benefits

    Despite the intuitive appeal of the argument, ‘‘benefits should improve offender outcomes

    and thereby reduce recidivism,’’ there is no direct, causal evidence to support or refute this

    claim. If benefits extend the affordability of basic needs and services like food, housing,

    drug treatment, physical and mental heath services, etc. (Allard 2002; Mohan and Lower-

    3 The closest source to a nationally representative picture we could locate comes from the Bureau of Justice Statistics Inmate Survey, which provides limited information on welfare receipt before an arrest and during an offender’s childhood. This survey does not track offenders over time.

    744 J Quant Criminol (2018) 34:741–773

    123

    Basch 2014; Mauer and McCalmont 2013; Godsoe 1998), then providing benefits should

    reduce the need for (and causes of) criminal behavior, thereby decreasing the likelihood of

    reoffending (Petersilia 2003). At least some empirical research supports such associations

    between poverty, state supports and recidivism (Holtfreter et al. 2004).

    On the other hand, benefits may also be counterproductive as a means of reducing

    recidivism, particularly in the case of drug offenders. One possibility is that benefits

    provide drug users with additional purchasing power that allows them to substitute pur-

    chases of other goods for more drugs (Johnson et al. 1985). If more income leads to greater

    drug use, providing benefits may serve to increase recidivism rates among beneficiaries.

    Alternatively, recipients may fraudulently trade their benefits for drugs or for cash used to

    purchase drugs (Roebuck 2014; Statement of the Honorable Phyllis K. Fong Inspector

    General 2012; Oregon Revised Statute §411.119 2005).4 Receipt of benefits could also

    reduce the pressures to engage in other prosocial behaviors during the post-release period,

    e.g., consistent job-seeking or more frequent visitation with supervision officers.

    Another consideration is that SNAP and TANF programs serve different (but over-

    lapping) populations, such that their potential importance to offenders and ultimately

    corrections systems should also vary along these dimensions. For example, the proportion

    of adult males receiving SNAP (around 44% of adult participants) is much higher than for

    TANF (around 15% of adult participants) (US Department of Agriculture 2017; US

    Department of Health and Human Services 2016). This implies that changes pertaining to

    SNAP are more likely to have the greatest impact on prisons, where males make up the

    majority of inmates. Conversely, female prison populations would be more impacted by

    restrictions to TANF. Such variations help to explain potential differences in impacts we

    might find between men and women.

    As another example, consider that nearly 20% of SNAP households are nondisabled,

    childless adult households, while only 6% of TANF households are single-member

    households. If offenders tend to be young individuals without children, then understanding

    how SNAP benefits can affect outcomes becomes more relevant to understanding how the

    ban may or may not affect change. Such nuances are critical to understanding how pro-

    grams may (or may not) translate to the impacts we test for in our analysis.

    Using the Ban as a Natural Experiment for Denying Benefits

    The goal of this paper is to test these competing theories using state variation in imple-

    mentation of the drug felony ban as a natural experiment. Specifically, our goal is to

    determine whether changes to the drug felony ban led to material changes in the rate of

    recidivism for the prison population of drug offenders. To do this, we tested the impact of

    the ban by looking at differences in recidivism for offenders convicted before and after the

    ban’s initial adoption. Earlier iterations of this paper also considered whether interim

    changes (i.e., modifications) to the ban’s application impacted offender outcomes. How-

    ever, because these changes occur on the basis of calendar date rather than conviction date,

    the strength of our identification is arguably weaker and results are less informative. As a

    result we have excluded these analyses from the paper. Nevertheless it can be noted that

    results from these additional analyses were consistent with the findings of this paper.

    4 In fact, there is explicit mention of trading benefits for drugs and the associated penalties in the SNAP benefit application form in Louisiana. (http://www.dcfs.louisiana.gov/assets/docs/searchable/ EconomicStability/Applications/OFS4_4I.pdf).

    J Quant Criminol (2018) 34:741–773 745

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    Across 10 states where we tested impacts for men and women (16 tests altogether), none

    showed significant changes resulting from ban modification.

    Later sections describe the data and methods we used for this analysis in greater detail;

    however, an important, upfront acknowledgement is that our data do not allow us to

    identify individual eligibility (or receipt) of benefits for specific offenders. Thus we cannot

    estimate the ban’s impact as it affected specifically those whose eligibility was altered or

    denied by the ban. Instead, we estimate the impact of the ban as it was ‘‘assigned’’ (by its

    passage) to all offenders, regardless of eligibility. In the parlance of statistical evaluation,

    our estimated treatment effect is modeled using an ‘‘intent-to-treat’’ (ITT) framework,

    rather than as an estimate of the ‘‘treatment on the treated’’ (TOT) (Angrist 2006). Nev-

    ertheless our investigation does inform an important policy-level consideration: Can

    removal or modification of the ban reduce the size of the prison population? Will it result

    in savings for corrections agencies?

    Such questions are even more important when considering whether the ban ever led to

    actual changes in the practices it was meant to influence in the first place. For example,

    Butcher and LaLonde (2006) show that in Cook County, Illinois, bans on TANF receipt did

    not significantly affect attachment to the welfare system for drug felons.5 Whatever the

    reason, such a finding implies that removal of the ban will have no impact since, as it is

    designed, it does not achieve its primary goal of denying benefits. In cases such as this, the

    question of ‘‘do benefits matter?’’ is secondary to the policy concern, ‘‘does the ban work?’’

    Our ITT analysis informs a question much like the latter—‘‘does the ban create meaningful

    system-level change?’’

    State Implementation of the Drug Felony Ban

    Since the PRWORA became law, states have varied considerably in their response to the ban

    and the timing of that response.Within 18 months of PRWORA enactment, 4 states had opted

    out of the ban entirely; today that number has grown to14.6 Twenty-six states havemodified the

    ban to allow benefits, subject to additional requirements imposed on drug felons specifically.

    Ten states have not altered their use of the ban at all. Thoughwe could not confirm the status of

    Wyoming’s laws, best indications are that Wyoming has a full ban in place.

    States’ initial adoption of the ban can be classified as one of three types of changes: (1)

    moving from no ban to a full ban, (2) moving from no ban to a partial ban, or (3) opting out

    immediately. One state with available data opted out immediately: New York.

    The meanings of full ban and no ban are clear: full ban implies total adoption of the

    PRWORA provision (i.e., felony drug offenders are completely barred from receiving

    SNAP or TANF benefits) and no ban implies no ban was in place (i.e., felony drug

    offenders do not face special conditions). The meaning of partial ban is more ambiguous.

    States with partial bans impose at least some special conditions for eligibility, and in

    5 The analysis of Butcher and LaLonde raises an interesting question of whether state agencies are in fact complying with the federal law. Though we cannot say with absolute certainty that every state complies, evidence gathered for this research (e.g., SNAP application forms asking about drug conviction status, and a conversation with a Massachusetts congressional representative) suggests that policies have resulted in operational changes at the agency level. (http://www.dcfs.louisiana.gov/assets/docs/searchable/ EconomicStability/Applications/OFS4_4I.pdf). 6 Gabor and Botsko (1998) report that 10 states opted out of the ban on food stamps in the year following the PRWORA ban. Those results were based on a survey of states and only report responses for the food stamp portion of the ban. Our independent research has led us to conclude that only 4 states had fully opted out of both aspects of the ban (i.e. completely removed restrictions to both SNAP and TANF).

    746 J Quant Criminol (2018) 34:741–773

    123

    practice, these conditions can vary considerably across states.7 For example in Iowa, drug

    felons are only eligible for benefits if they participate in drug treatment. In Louisiana, drug

    felons only become eligible one year after their release. In Florida, drug felons convicted of

    possession are eligible, while those convicted of trafficking are not. Given the hetero-

    geneity within states’ use of partial bans, we do not to attempt to tease out impacts of

    various forms of partial restrictions. That is to say that we do not attempt to measure

    differential impacts between, e.g., ‘‘random drug testing’’ and ‘‘required drug treatment.’’

    Finally, it should be noted that while the PRWORA itself denied benefits to all

    offenders for SNAP and TANF simultaneously, modifications have sometimes addressed

    these programs separately, in both substance and timing. For example, Washington first

    removed the ban on SNAP benefits in October 2004, then removed the ban on TANF

    benefits almost a year later, in September 2005. Changes of this nature are the exception

    rather than the rule; most states have modified both SNAP and TANF eligibility

    requirements at the same time (Ekstrand 2005).

    Data

    For this study, we combined prison data, legislative data and county-level data compiled by

    the US Census to construct a single analytic dataset. Prison data come from the National

    Corrections Reporting Program (NCRP)—an annual data collection program (operated by

    the Bureau of Justice Statistics) that collects prison admission and release data for indi-

    vidual offenders in every state across the US These offender-level data include information

    on offender characteristics such as sex, age and race, and sentence information such as

    offense type, time spent in prison and sentence length.

    Though NCRP data go back as far as 1983, known issues with data reliability make

    much of the early data problematic (Rhodes et al. 2012; Neal and Rick 2014; Pfaff 2011).

    More recently, NCRP data collection and assembly have been redesigned to provide more

    reliable information (Rhodes et al. 2012). Data are now constructed as longitudinal, panel

    datasets (called ‘‘term files’’) tracking individual offenders and their movements into and

    out of prison over a given reporting period (Luallen et al. 2012). Reporting periods covered

    in the NCRP data vary from state to state, with the most common window beginning in

    January 2000 and extending to December 2014.

    There are only six states in the NCRP with data extending back to 1996 where impact

    estimates are possible: California, Florida, Georgia, Illinois, Michigan, andMinnesota.8 Given

    that our interest is in analyzing the impact of the banwhen itwas first passed in 1996, only these

    states can provide an unbiased sample of offenders who entered prison during that time.

    We also assembled legislative data on a state-by-state basis so that we could control for

    state-level changes in ban use over time. We compiled this data using multiple sources.

    One source was the ‘‘State Options Reports’’ published by the Food and Nutrition Service

    (FNS) (US Department of Agriculture 2016). These survey-based reports provide high-

    7 Broadly, states adopt three types of partial reforms: (1) requirements for offenders to participate in or complete treatment before receiving benefits; (2) allowance for drug offenders who committed less serious crimes to access benefits; and (3) allowance for offenders to receive benefits after a probationary period following release. 8 New York has data back going back to 1994, but opted out immediately after the ban was passed. We separately tested our pooled estimation with and without New York and found no difference in findings between models.

    J Quant Criminol (2018) 34:741–773 747

    123

    level summaries of each state’s policies regarding the drug ban and modifications thereof.

    They extend back to 2002 and are typically published once every one to two years. We

    augmented these reports with independent web searches and queries in a legal database

    (Westlaw). In a number of cases our search results conflicted with the FNS reports.9 In

    those cases, we disregarded the FNS survey data in favor of source documents.

    Table 1 below provides a summary of relevant state laws and NCRP reporting windows

    for all 50 states. Though our sample used only a subset of these states, the complete

    table provides a useful resource for researchers. It does not document every legal change that

    has occurred over time; rather, it describes major policy shifts as defined earlier in this paper.

    Finally, we supplemented these data with county-level information compiled by the US

    Census Bureau. These data include county-level descriptions of population density, eco-

    nomic conditions (such as poverty rates and household income), education level and SNAP

    participation rates. Most of these data are made available through Census’s USA counties

    data products, though some information (including rates of SNAP recipiency) is reported

    as part of Census’s intercensal estimates.

    Method

    To estimate the impact of the ban, we combined two popular inferential methods for

    estimating causal effects: regression discontinuity (RD) design and difference-in-differ-

    ences (DiD) estimation. Our use of RD design provides defensible measures of causal

    impacts by minimizing observed and unobserved differences between comparison groups.

    Our use of second-differencing (DiD) strengthens the credibility of these results by con-

    trolling for other possible coincident, exogenous shocks that may also have impacted

    recidivism but were not the result of the ban. We explain our use of each.

    The motivation for our quasi-experimental approach is straightforward. Consider first a

    simple approach that estimates ban impacts as the unadjusted pre-post comparison between

    treated and untreated groups (in this case, average outcomes before vs. after the ban). In

    order for estimates to be unbiased, before and after groups must be characteristically

    equivalent with respect to measures correlated with the outcome. That condition is unlikely

    to hold without adjustment; however, even with adjusted comparisons one cannot reject

    that possibility that unobserved group differences correlated with the outcome still exist.

    The problem worsens when unobserved differences are changing (or trending) in the pre

    and post periods. Quasi-experimental methods can overcome such limitations and, in the

    context of our analysis, we use RD to do this.

    RD designs operate under a simple premise: unbiased treatment effects can be identified

    when the probability of treatment is a discontinuous function of one or more underlying

    measures (Imbens and Lemieux 2008; Cameron and Trivedi 2005), also called forcing

    variables. Discontinuities occur at specific thresholds (or cutoffs), such that treatment

    assignment depends (discontinuously) on whether individuals fall above or below the

    cutoff. By extension, when individuals have imprecise control over the assignment to

    treatment, treatment–control comparisons in a local neighborhood around the cutoff can be

    analyzed like randomized experiments (Lee and Lemieux 2010). That is to say that nearby

    9 Apparent confusion by states as to what is meant by ‘‘ban modification’’ has led to reporting error in the State Options Report, and subsequently, confusion in the literature as to what states have adopted what policies and when. For example, although Iowa imposes some drug rehabilitation services (or other requirements) for former drug felons, FNS reports show it has opted out since 2006.

    748 J Quant Criminol (2018) 34:741–773

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    Table 1 (a) List of ban modification statutes and enactment dates identified for analysis, (b) dates and statutes ban modifications used in analysis

    State Modification 1 Modification 2 NCRP

    Type Date Bill/law Type Date Bill/law Start End

    (a)

    Alabama None NA – NA NA – 2007 2014

    Alaska None NA – NA NA – 2005 2013

    Arizona None NA – NA NA – 2000 2014

    Arkansas Partial 4/1/97 Ark. Code Ann. § 20-76-409 H.B.1295

    NA NA – – –

    California Partial 7/1/05 AB 1796/Cal. Welf. and Inst. Code § 18901.3

    Opted- out

    4/1/ 15

    AB 1468 § 49 1992 2014

    Colorado Partial 7/1/97 Colo. Rev. Stat. §§ 26-2-305, 26-2-706

    NA NA – 2000 2014

    Connecticut Partial 6/18/97 PA 97-2/Conn. Gen. Stat. § 17b-112d

    NA NA – – –

    Delaware Partial 7/17/03 HB 263/Del. Code Ann. tit. 31, § 605

    Opted- out

    7/1/ 11

    SB 12/31 Del. C. § 512

    2009 2014

    Florida Partial 5/30/97 Fla. Stat. Ann. ch. 414.095

    NA NA – 1996 2014

    Georgia None NA – NA NA – 1971 2014

    Hawaii Opted- out

    6/16/97 HB No. 480/Haw. Rev. Stat. § 346-53.3

    NA NA – – –

    Idaho Partial 7/1/00 HB 627/Idaho Code § 56-202

    NA NA – 2008 2012

    Illinois Partial 7/1/97 730 Ill. Comp. Stat 5/1-10

    NA NA – 1989 2013

    Indiana Partial 7/1/05 SB 523/Ind. Code § 12-20-16-6

    NA NA – 2002 2014

    Iowa Partial 1/11/97 HF 20/Iowa Code § 239B.5

    NA NA – 2006 2014

    Kansas Partial 7/1/06 HB 2861/SB 243 NA NA – 2011 2014

    Kentucky Partial 7/15/98 Ky. Acts ch. 427, sec. 12/KRS § 205.2005

    NA NA – 2000 2013

    Louisiana Partial 7/1/97 No. 1351/LSA- R.S. 46:233.2

    NA NA – – –

    Maine Opted- out

    4/2/02 H.P. 1665 L.D. 2170/Me. Rev. Stat. Ann. tit. 22, §§ 3104(14), 3762(17)

    NA NA – 2012 2014

    Maryland Partial 7/1/00 Md. Ann. Code 88A, §§ 50A, 65

    Opted- out

    10/ 1/ 07

    Acts 2007, c. 3, §8

    2000 2012

    J Quant Criminol (2018) 34:741–773 749

    123

    Table 1 continued

    State Modification 1 Modification 2 NCRP

    Type Date Bill/law Type Date Bill/law Start End

    Massachusetts Partial 12/1/01 2001 MA. Adv. Legis. Serv. 177, § 4400-1000

    NA NA – 2010 2014

    Michigan Partial 8/18/97 1997 Mich. Pub. Acts 109, § 622

    NA NA – 1989 2013

    Minnesota Partial 7/1/97 SF 1/MN. Stat. § 256D.024

    NA NA – 1994 2014

    Mississippi None NA – NA NA – 2004 2014

    Missouri Partial 8/28/14 SB 680/MO. Stat. § 208.247

    NA NA – 2000 2014

    Montana Partial 7/1/05 SB 29/MT. Stat. 53-4-231

    NA NA – 2010 2014

    Nebraska Partial 5/13/03 LB 667/Neb. Rev.Stat. § 68-1017.02

    NA NA – 2000 2014

    Nevada Partial 1/1/98 Nev. Rev. Stat § 422.29316

    NA NA – 2008 2014

    (b)

    New Hampshire

    Opted- out

    8/1/97 N.H. Rev. Stat. Ann. § 167:81-a

    NA NA – 2011 2014

    New Jersey Partial 11/1/96 No. 15/N.J. Stat. Ann. § 44:10-48

    Opted- out

    11/ 1/ 09

    No. 4197/N.J. Stat. Ann. § 44:10-48.1

    2003 2013

    New Mexico Opted- out

    5/15/02 HB 11/N.M. Stat. Ann. § 27-2B- 11(c’)

    NA NA – 2010 2014

    New York Opted- out

    8/1/97 N.Y. Laws § 121436

    NA NA – 1994 2014

    North Carolina

    Partial 7/1/97 N.C. Gen. Stat. § 108A-25.2

    NA NA – 1999 2014

    North Dakota None NA – NA NA – 2002 2014

    Ohio Opted- out

    10/16/09 HB 1/Ohio Rev. Code Ann. § 5101.84

    NA NA – 2009 2013

    Oklahoma Opted- out

    6/13/97 HB 2170/1997 Okla. Sess. Law Serv. Ch. 414

    NA NA – 2000 2014

    Oregon Opted- out

    7/1/97 Or. Rev. Stat. § 411.119 Ch. 581 S.B. No. 825

    Partial 8/ 16/ 05

    Ch. 706 H.B No. 2485 OR ST 411.119

    2001 2013

    Pennsylvania Partial 12/23/03 HB 44/62 Pa. Stat. § 405.1(i)

    NA NA – 2001 2014

    750 J Quant Criminol (2018) 34:741–773

    123

    the cutoff, groups are assumed to be characteristically equivalent along observed and

    unobserved measures.

    For our analysis, we used this logic of RD design to identify ban impacts. In this case,

    treatment is identified on the basis of conviction date—felons convicted on or before

    August 22, 1996 were eligible for benefits upon release and those convicted after were not.

    The date of conviction acts as the forcing variable and the discontinuity is estimated as the

    average difference in outcomes for offenders convicted just before and just after August

    22.10 We used prison admission date as a proxy for conviction date because we do not

    observe actual date of conviction.11

    Table 1 continued

    State Modification 1 Modification 2 NCRP

    Type Date Bill/law Type Date Bill/law Start End

    Rhode Island Opted- out

    7/1/04 Family Independence Act Amendment/ R.I. Gen. Laws §§ 40-5.1-8, 40-6-8

    NA NA – 2004 2014

    South Carolina

    None NA – NA NA – 2000 2014

    South Dakota Opted- out

    3/5/09 HB1123/SDCL § 28-12-3

    NA NA – 2000 2012

    Tennessee Partial 5/14/02 Tenn. Code Ann. §§ 71-3-154, 71-5-308

    NA NA – 2000 2014

    Texas None NA – NA NA – 2005 2014

    Utah Partial 7/4/97 Utah Code Ann. § 35A-3-311

    NA NA – 2000 2014

    Vermont Opted- out

    Unknown 1997 Vt. Laws 61, § 131

    NA NA – – –

    Virginia Partial 3/22/05 § 63.2-505.2 NA NA – – –

    Washington Partial 10/1/98 HB 3901/Wash. Rev. Code § 74.08.025

    Opted- out

    9/1/ 05

    SB 6411/Wash. Rev. Code § 74.08.025

    2000 2014

    West Virginia None NA – NA NA – 2006 2014

    Wisconsin Partial 10/1/97 Wis. Stat. §§ 49.79, 49.145, 49.148

    NA NA – 2000 2014

    Wyoming None NA – NA NA – 2006 2014

    10 A large number of studies have used date/time as an assignment variable modeled within an RD framework. Table 5 in Lee and Lemieux (2010) provides a nice summary of many such studies. Because time is the forcing variable, our approach can also be described as an ‘‘event study’’—language more common to various social science disciplines. 11 We argue that prison admission is a good proxy for date of conviction. Prior to conviction, most offenders are housed in jails rather than prisons. After conviction, most offenders are moved to prison quickly.

    J Quant Criminol (2018) 34:741–773 751

    123

    To be credible, RD analysis requires some assumptions be met. One assumption

    (mentioned above) is that individuals do not have precise control over their treatment

    status. In this case, it is to say that offenders (as well as prosecutors, defenders and judges)

    do not precisely control the timing of conviction. Where this assumption is not met,

    systematic selection in the timing of drug convictions can threaten validity. Given the

    power that attorneys and judges possess, we cannot dismiss that possibility that gaming of

    conviction dates can occur; however, we argue it is unlikely that prosecutorial or sen-

    tencing practices were manipulated to systematically favor some drug offenders over

    others.

    To test whether there is any evidence that manipulation in convictions around the date

    of the cutoff (August 22) occurred, we borrow from an empirical test offered in Jacob et al.

    (2012). Specifically, we construct two local linear regressions, one to the left of the cutoff

    and one to the right, that model the percent of sampled drug offenders admitted during each

    week (as the dependent variable) over time (as the independent variable). We then test

    whether the intercepts just to the left and just to the right are statistically different from one

    another. Estimated intercepts and their differences before and after the cutoff are reported

    in Table 2 for both men and women using a 6-month window of drug offender admissions.

    Overall these results confirm there is no evidence of systematic manipulation in convic-

    tions around the cutoff.

    Another assumption of our RD design is that no other changes occurred simultaneously

    with the timing of the ban that affected recidivism for reasons other than the ban itself.

    Though we were not able to find any evidence that such a change took place, we cannot

    directly prove or disprove this condition exists. Instead, we overcome this limitation by

    incorporating DiD estimation as part of our identification strategy. Specifically, we com-

    pared changes around the ban for drug offenders (a group affected by the ban) to similar

    changes around the ban for nondrug offenders (a group not affected by the ban). In the

    language of difference-in-differences, estimated impacts within groups (before vs. after)

    are first differences, and differences in impacts across groups (drug vs. nondrug) are second

    differences.

    The strength of the DiD estimator is that it zeros out bias (in estimated first differences)

    resulting from unobserved changes also affecting recidivism and closely coinciding with

    the ban. To accomplish this, DiD identification assumes a constant bias among compared

    groups such that any unobservable bias impacts groups equally in the absence of treatment

    (Lechner 2010; Angrist et al. 2009). Thus our application assumes that factors affecting

    changes in recidivism around the time of, but not as a result of, the ban affect drug and

    nondrug offenders equally. Traditional DiD models also assume that groups follow similar

    trends absent the treatment (or ‘‘constant trends’’); however, because our impacts are

    estimated as discontinuous jumps (i.e., using RD), assumptions about constant trends are

    not necessary.

    Using this framework, we examined the data in two ways. First, we generated graphical

    illustrations depicting observed prison return rates for offenders convicted just before and

    after the ban. Descriptive graphics of this kind are commonly used in regression discon-

    tinuity analyses because they can provide useful insights about the nature of the impact

    being estimated and the strength of the identification. Second, we estimated DiD impacts

    using Cox-proportional hazards models—models that are well known to the literature on

    survival estimation (Cameron and Trivedi 2005; Klein and Moeschberger 2003; Allison

    2010). We present the equations and discuss the details of our model specification below.

    Equations (1) and (2) estimate the probability of reincarceration for offenders released

    from prison as a function of time at risk. Risk of reincarceration begins on the day an

    752 J Quant Criminol (2018) 34:741–773

    123

    offender exits prison, and offenders are followed until a known event occurs or until the

    end of the data window, at which point the data are right-hand censored. Offenders are

    followed for as long as the NCRP data currently allow—until December 31, 2014 in most

    cases.

    Both equations share the same specification but are estimated on different samples (drug

    and nondrug offenders). For drug offenders, we estimate:

    kdij t Tij;Pre; Tij;Post;Ban;M;Xij;Cj � �

    � �

    ¼ kd0ðtÞe ðb1Tij;Preþb2Tij;Postþsd ðBanÞþqdðMÞþpXdijþlCdj Þ ð1Þ

    Similarly, for nondrug offenders we estimate:

    kndij t Tij;Pre; Tij;Post;Ban;M;Xij;Cj � �

    � �

    ¼ knd0 ðtÞe ða1Tij;Preþa2Tij;Postþsnd ðBanÞþqnd ðMÞþdXndij þlCndj Þ ð2Þ

    In both equations,

    kijðtÞ is the probability of return to prison for the ith offender from the jth county as a function of time (t) since release from prison; superscript d denotes drug offenders;

    superscript nd denotes nondrug offenders.

    k0ðtÞ is the baseline hazard function common to all offenders, also a function of time since release; again superscript d indicates drug offenders; nd denotes nondrug

    offenders.

    t is time since prison release, beginning at zero and increasing by one each day an

    offender is at liberty.

    Tij;Pre is the number of days before PRWORA enactment, based on prison admission

    date for the ith offender from the jth county. Admissions after enactment have a value of

    zero.

    Table 2 Estimated proportion of sample admitted (weekly) to prison around the cutoff (august 22nd)

    Men Women

    Left Right Difference Left Right Difference

    Pooled 0.019** (0.001)

    0.021** (0.001)

    -0.001 (0.002)

    0.017** (0.002)

    0.019** (0.002)

    -0.002 (0.002)

    CA 0.020** (0.001)

    0.021** (0.001)

    -0.001 (0.002)

    0.018** (0.002)

    0.021** (0.002)

    -0.002 (0.002)

    FL 0.020** (0.002)

    0.021** (0.002)

    -0.002 (0.002)

    0.017** (0.003)

    0.016** (0.003)

    0.001 (0.004)

    GA 0.017** (0.002)

    0.017** (0.002)

    0.000 (0.002)

    0.016** (0.005)

    0.014** (0.004)

    0.002 (0.006)

    IL 0.019** (0.002)

    0.021** (0.001)

    -0.002 (0.002)

    0.016** (0.003)

    0.019** (0.003)

    -0.002 (0.004)

    MI 0.016** (0.002)

    0.023** (0.002)

    -0.007* (0.003)

    0.016** (0.005)

    0.026** (0.005)

    -0.010 (0.006)

    MN 0.019** (0.004)

    0.020** (0.004)

    0.000 (0.005)

    0.044** (0.015)

    0.046** (0.009)

    -0.002 (0.018)

    Standard errors are reported in parentheses. Stars denote p-values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value\0.01. Numbers are subject to rounding error

    J Quant Criminol (2018) 34:741–773 753

    123

    Tij;Post is the number of days after PRWORA enactment, based on prison admission date

    for the ith offender from the jth county. Admissions before enactment have a value of

    zero.

    Ban is an indicator variable equal to 1 if an offender was admitted to prison after

    PRWORA.

    M is a time-varying covariate for ban modification. It is specified as an indicator variable

    equal to 1 if an offender is at liberty to fail in a period where a modified ban has been

    introduced. This variable will only take on a value of 1 if the modified ban was

    introduced more than a year after PRWORA. Modified bans introduced within a year of

    PRWORA are characterized as part of the impact of the initial change.

    Xij is a vector of individual characteristics for the ith offender from the jth county

    including age at the time of release from prison, time served in prison and year of

    release.

    Cj is a vector of county-level characteristics for the ith offender from county j, including

    percentage of households in poverty, median household income, local unemployment,

    adult population density and high school education.

    For these equations: (b1 and b2) and (a1 and a2) capture the time trends in outcomes before and after the ban for drug offenders and nondrug offenders respectively; sd and snd

    represent the treatment effect of the ban (i.e., the first difference) for drug offenders and

    nondrug offenders respectively; qd and qnd represent the average difference in outcomes for drug and nondrug offenders in the modified period; and p, d and l capture other baseline differences in offender and community characteristics.

    Equation (3) estimates the overall impact of the ban as the difference between estimated

    treatment effects between groups. For this equation, sd and snd are defined as before and the second difference, Ds, describes the impact of the ban itself.

    Ds ¼ ŝd � ŝnd ð3Þ

    There are other practical considerations for our estimation. The first is how to identify/label

    offenders as drug offenders subject to the ban. This is challenging because (1) offenders can be

    chargedwithmultiple offenseswithvaryingdegreesof seriousness; (2)NCRPdataonly records

    the top three,most serious offenses; (3)NCRPdata do not denotewhich conviction offenses are

    felonies and which are misdemeanors, a criterion for the application of the ban; and (4) drug

    crime admissions can be for revocations (where no new conviction occurs), rather than for new

    crimes that are subject to the ban (because a conviction does occur).

    Given these limitations, we identify (a) drug offender status based on offense type for

    the first two convicted sentences; and (b) admission status based on the type of admission

    labeled in the NCRP, i.e., restricting the sample to new court commitments only.12 We also

    conducted a sensitivity analysis that defined a drug offender using the first offense only and

    found results were substantively unchanged. Drug offender status is also carried forward so

    that, once observed, an offender is labeled a drug offender even when readmitted for a

    nondrug offense. Nondrug offenders are defined as offenders with no prior conviction for a

    drug offense.

    12 \15% of offenders in our analytic sample are convicted of more than two offenses and, of these,\2% have nondrug offenses for their first two offenses and a drug-related offense for their third offense. Since we cannot know whether this third offense is a felony or misdemeanor, we treat these cases as nondrug offenders.

    754 J Quant Criminol (2018) 34:741–773

    123

    A second consideration is determining the optimal size of the interval around the cutoff.

    Larger intervals provide bigger samples for analysis and improve statistical power, but

    increase the potential for omitted variable bias, especially from poorly specified trends.

    Conversely, smaller intervals provide the most robust identification but may be too

    imprecise to reject the null even where true impacts exist. To achieve a balance in light of

    these tradeoffs, we report estimates across multiple intervals around the cutoff. Specifi-

    cally, we estimate and compare impacts from four samples of offenders convicted (±)

    6 months, 1, 2, and 3 years around the cutoff. This allows us to better judge the overall

    strength and robustness of our findings.

    Tables 3 and 4 report the size of each sample and observed returns to prison for male

    and female populations (respectively) in each state and for the pooled sample. Drug and

    nondrug offenders are reported separately. Overall these tables show that most samples are

    sufficiently sized to detect moderate to large differences in most cases, and small differ-

    ences in at least some states (particularly in California, Florida, Georgia, Illinois and the

    pooled sample).13

    A third consideration is how to estimate impacts on the pooled sample of states.

    Specifically, estimates can be weighted so that they represent (a) the average impact across

    individuals or (b) the average impact across states. Each statistic says something different

    and, without a specific application in mind, it is not clear which one is more interesting

    from a policy perspective. Estimates giving equal weight to individuals will naturally over

    represent larger states (such as California) and, in turn, idiosyncratic patterns of practice;

    however, they will be more precise than estimates weighing states equally. Our solution for

    this paper is to report both sets of pooled estimates: those weighting individuals equally

    (shown in Tables 5 and 6) and those weighting states equally (shown in Table 7).

    A fourth concern is how to best specify time trends in estimation. More flexible time

    trends modeled using higher-order polynomials may provide better fits to the data (relative

    to simple linear trends), but can suffer from overfitting and run a greater risk of introducing

    bias as a result (Gelman and Imbens 2014). To address this concern, we (1) visually

    inspected the data to determine the best approach, and (2) tested the sensitivity of our

    results to alternative specifications. Based on the results of our inspections (presented in

    ‘‘Graphical Analyses’’), we adopted an approach using simple linear trends to model the

    discontinuity, and tested the robustness of these models against quadratic and third-order

    specifications of time trends.

    Finally, an important consideration for estimation is that admission cohorts in two

    states, Florida and Minnesota, do not extend a full three years (i.e., 36 months) back from

    August 22, 1996. In Florida, admission cohorts begin January 1, 1996 (6 months before)

    and in Minnesota they begin January 1, 1994 (30 months before).

    The implication for this design is that cohorts of offenders are not evenly observed in

    the data. Offenders admitted before the start of a term file window are only observed when

    released during a term file year. In the case of Florida, offenders convicted January 1, 1995

    are only observed if they served at least one full year in prison (i.e., released sometime

    after January 1, 1996). Those serving 364 days (i.e., released December 31, 1995) are

    unobserved and thus omitted from the sample.

    13 For reference, computations of detectable effects performed in Stata (using the stpower command) show that sample sizes of 200, 500, 3,000, and 10,000 can detect minimum differences in recidivism rates of roughly 0.40, 0.25, 0.10, and 0.05 respectively. These computations assume a two-sided test of a Cox model where the standard deviation of the Ban/Mod covariate is 0.5, power is 0.8, and alpha is 0.05.

    J Quant Criminol (2018) 34:741–773 755

    123

    Given that term file windows in all states overlap the ban implementation date, uneven

    sample selection is not a fundamental threat to our identification strategy; however, bias

    may still result if trends in observed recidivism leading up to the ban are not adequately

    controlled for. As before, graphical illustrations (shown in the ‘‘Appendix’’) provide a

    Table 3 Sample sizes for drug offenders and returns to prison in each state

    Sex Sample N Pooled CA FL GA IL MI MN

    Men 6-month Total 32,417 16,331 4778 3032 6692 1226 358

    Returning 18,204 8811 2652 1620 4340 578 203

    1-year Total 65,617 33,138 9569 6077 13,673 2445 715

    Returning 36,856 17,816 5392 3262 8849 1141 396

    2-year Total 129,815 65,346 18,426 11,999 27,519 4981 1544

    Returning 72,932 35,191 10,427 6398 17,728 2338 850

    3-year Total 192,928 95,231 28,113 18,454 41,222 7473 2435

    Returning 108,534 51,328 16,062 9770 26,557 3470 1347

    Women 6-month Total 4474 2468 579 383 885 115 44

    Returning 2325 1357 247 156 503 44 18

    1-year Total 9201 5053 1269 718 1809 251 101

    Returning 4789 2796 529 297 1035 95 37

    2-year Total 17,907 9796 2415 1442 3449 565 240

    Returning 9233 5416 998 577 1941 211 90

    3-year Total 26,270 14,216 3656 2177 5063 817 341

    Returning 13,427 7738 1536 857 2852 307 137

    Table 4 Sample sizes for nondrug offenders and returns to prison in each state

    Sex Sample N Pooled CA FL GA IL MI MN

    Men 6-month Total 100,984 58,888 13,057 8063 11,839 6574 2563

    Returning 65,702 42,447 6528 4122 7591 3389 1625

    1-year Total 205,374 120,294 26,102 16,885 23,877 13,076 5140

    Returning 133,638 86,610 13,173 8711 15,319 6603 3222

    2-year Total 405,179 238,304 48,778 33,277 48,561 26,097 10,162

    Returning 264,425 171,992 24,547 17,107 31,242 13,143 6394

    3-year Total 599,597 351,432 69,568 51,234 73,000 39,173 15,190

    Returning 390,753 253,498 34,984 26,206 46,938 19,665 9462

    Women 6-month Total 8940 5218 958 1003 1110 481 170

    Returning 5133 3388 354 452 638 216 85

    1-year Total 17,992 10,541 1962 1917 2276 932 364

    Returning 10,370 6891 732 840 1332 398 177

    2-year Total 35,423 20,829 3659 3693 4611 1883 748

    Returning 20,467 13,689 1341 1574 2700 804 359

    3-year Total 52,024 30,469 5226 5524 6787 2912 1106

    Returning 29,920 19,912 1929 2342 3972 1252 513

    756 J Quant Criminol (2018) 34:741–773

    123

    T a b le

    5 E st im

    at ed

    im p ac ts

    am o n g w o m en

    u si n g p o o le d sa m p le

    W in d o w

    ar o u n d cu to ff

    6 -m

    o n th

    1 -y ea r

    2 -y ea r

    3 -y ea r

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    B an

    1 .0 1 1

    0 .0 8 8

    0 .9 9 5

    0 .0 5 7

    0 .9 9 6

    0 .0 6 0

    1 .0 1 3

    0 .0 4 1

    1 .0 1 7

    0 .0 4 3

    1 .0 1 0

    0 .0 2 9

    0 .9 6 4

    0 .0 3 3

    0 .9 9 1

    0 .0 2 3

    M o d ifi ca ti o n

    0 .3 2 5 * * *

    0 .0 5 5

    0 .2 9 6 * * *

    0 .0 3 6

    0 .3 3 0 * * *

    0 .0 3 9

    0 .3 6 6 * * *

    0 .0 3 0

    0 .3 7 3 * * *

    0 .0 3 0

    0 .3 9 7 * * *

    0 .0 2 2

    0 .3 8 9 * * *

    0 .0 2 5

    0 .4 2 1 * * *

    0 .0 1 9

    % in

    P o v er ty

    1 .0 0 7

    0 .0 1 4

    0 .9 9 9

    0 .0 0 8

    1 .0 0 1

    0 .0 1 0

    0 .9 9 6

    0 .0 0 6

    1 .0 0 6

    0 .0 0 7

    0 .9 9 1 *

    0 .0 0 4

    1 .0 0 0

    0 .0 0 6

    0 .9 9 2 *

    0 .0 0 4

    M ed ia n in co m e

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    U n em

    p lo y m en t

    1 .0 2 8 *

    0 .0 1 5

    1 .0 4 5 * * *

    0 .0 0 9

    1 .0 1 6

    0 .0 1 0

    1 .0 4 3 * * *

    0 .0 0 7

    1 .0 2 6 * * *

    0 .0 0 7

    1 .0 4 4 * * *

    0 .0 0 5

    1 .0 2 7 * * *

    0 .0 0 6

    1 .0 4 0 * * *

    0 .0 0 4

    P o p u la ti o n d en si ty

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    P er ce n t o f H S ed u ca te d ad u lt s

    1 .0 2 4 * *

    0 .0 0 8

    1 .0 1 2 * *

    0 .0 0 4

    1 .0 1 4 * *

    0 .0 0 5

    1 .0 1 2 * * *

    0 .0 0 3

    1 .0 1 3 * * *

    0 .0 0 4

    1 .0 1 3 * * *

    0 .0 0 2

    1 .0 1 2 * * *

    0 .0 0 3

    1 .0 1 3 * * *

    0 .0 0 2

    A g e at

    re le as e

    0 .9 7 3 * * *

    0 .0 0 3

    0 .9 8 4 * * *

    0 .0 0 2

    0 .9 7 4 * * *

    0 .0 0 2

    0 .9 8 3 * * *

    0 .0 0 1

    0 .9 7 6 * * *

    0 .0 0 1

    0 .9 8 4 * * *

    \ 0 .0 0 1

    0 .9 7 5 * * *

    0 .0 0 1

    0 .9 8 3 * * *

    \ 0 .0 0 1

    T im

    e- se rv ed

    1 .0 0 0 * *

    \ 0 .0 0 1

    0 .9 9 9 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    0 .9 9 9 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    R el ea se

    y ea r

    1 .0 5 3

    (0 .0 4 5 )

    1 .0 5 3

    (0 .0 4 5 )

    1 .0 0 3

    (0 .0 2 9 )

    1 .0 0 3

    (0 .0 2 9 )

    1 .0 2 4

    (0 .0 2 1 )

    1 .0 2 4

    (0 .0 2 1 )

    1 .0 1 4

    (0 .0 1 7 )

    1 .0 1 4

    (0 .0 1 7 )

    P re -t re n d

    0 .9 9 9

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    P o st -T re n d

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    1 .0 0 0

    J Quant Criminol (2018) 34:741–773 757

    123

    T a b le

    5 co n ti n u ed

    W in d o w

    ar o u n d cu to ff

    6 -m

    o n th

    1 -y ea r

    2 -y ea r

    3 -y ea r

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    S ta te

    F ix ed

    E ff ec ts

    Y es

    Y es

    Y es

    Y es

    Y es

    Y es

    Y es

    Y es

    N 1 3 ,1 7 7

    2 6 ,7 3 3

    5 2 ,4 9 0

    7 6 ,8 1 8

    E st im

    at ed

    D iD

    B an

    Im p ac t (D )

    0 .0 1 6

    – 0 .0 1 7

    0 .0 0 7

    – 0 .0 2 8

    0 .1 0 5

    0 .0 7 3

    0 .0 5 1

    0 .0 4 2

    T h is ta b le re p o rt s co ef fi ci en ts as

    d es cr ib ed

    in E q s. (4 )– (6 ), co n v er te d in to

    h az ar d ra ti o s. S ta n d ar d er ro rs ar e re p o rt ed

    in p ar en th es es . S ta rs d en o te p v al u es

    fo r st at is ti ca l te st s o f

    d if fe re n ce s fr o m

    ze ro : * in d ic at es

    a v al u e o f 0 .0 5 ; * * in d ic at es

    a v al u e o f 0 .0 1 ; * * * in d ic at es

    a v al u e o f 0 .0 0 1 . N u m b er s ar e su b je ct

    to ro u n d in g er ro r

    758 J Quant Criminol (2018) 34:741–773

    123

    T a b le

    6 E st im

    at ed

    im p ac ts

    am o n g m en

    u si n g p o o le d sa m p le

    W in d o w

    A ro u n d C u to ff

    6 -m

    o n th

    1 -y ea r

    2 -y ea r

    3 -y ea r

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    B an

    1 .0 1 3

    0 .0 3 1

    0 .9 7 8

    0 .0 1 6

    0 .9 9 6

    0 .0 2 1

    0 .9 9 7

    0 .0 1 1

    0 .9 7 6

    0 .0 1 5

    0 .9 9 8

    0 .0 0 8

    0 .9 6 7 * *

    0 .0 1 2

    0 .9 8 5 *

    0 .0 0 6

    M o d ifi ca ti o n

    0 .3 8 2 * * *

    0 .0 2 0

    0 .4 0 8 * * *

    0 .0 1 3

    0 .3 9 6 * * *

    0 .0 1 5

    0 .4 1 3 * * *

    0 .0 0 9

    0 .3 8 4 * * *

    0 .0 1 0

    0 .4 3 1 * * *

    0 .0 0 6

    0 .3 9 7 * * *

    0 .0 0 8

    0 .4 4 0 * * *

    0 .0 0 5

    % in

    P o v er ty

    0 .9 7 7 * * *

    0 .0 0 4

    0 .9 9 3 * *

    0 .0 0 2

    0 .9 8 9 * * *

    0 .0 0 3

    0 .9 9 4 * * *

    0 .0 0 2

    0 .9 8 9 * * *

    0 .0 0 2

    0 .9 9 3 * * *

    0 .0 0 1

    0 .9 8 9 * * *

    0 .0 0 2

    0 .9 9 1 * * *

    \ 0 .0 0 1

    M ed ia n in co m e

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    U n em

    p lo y m en t

    1 .0 2 5 * * *

    0 .0 0 5

    1 .0 3 7 * * *

    0 .0 0 3

    1 .0 2 2 * * *

    0 .0 0 4

    1 .0 3 5 * * *

    0 .0 0 2

    1 .0 2 1 * * *

    0 .0 0 3

    1 .0 3 3 * * *

    0 .0 0 1

    1 .0 1 9 * * *

    0 .0 0 2

    1 .0 3 0 * * *

    0 .0 0 1 1

    P o p u la ti o n d en si ty

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    P er ce n t o f H S ed u ca te d ad u lt s

    1 .0 1 3 * * *

    0 .0 0 2

    1 .0 2 0 * * *

    0 .0 0 1

    1 .0 1 3 * * *

    0 .0 0 2

    1 .0 2 0 * * *

    \ 0 .0 0 1

    1 .0 1 0 * * *

    0 .0 0 1

    1 .0 1 8 * * *

    \ 0 .0 0 1

    1 .0 0 9 * * *

    \ 0 .0 0 1

    1 .0 1 6 * * *

    \ 0 .0 0 1

    A g e at

    re le as e

    0 .9 8 7 * * *

    \ 0 .0 0 1

    0 .9 9 1 * * *

    \ 0 .0 0 1

    0 .9 8 7 * * *

    0 .0 0 1

    0 .9 9 0 * * *

    \ 0 .0 0 1

    0 .9 8 7 * * *

    \ 0 .0 0 1

    0 .9 9 0 * * *

    \ 0 .0 0 1

    0 .9 8 6 * * *

    1 .0 0 0

    0 .9 9 0 * * *

    \ 0 .0 0 1

    T im

    e- se rv ed

    1 .0 0 0 *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    R el ea se

    y ea r

    1 .0 3 4 * *

    (0 .0 1 3 )

    1 .0 3 4 * *

    (0 .0 1 3 )

    1 .0 2 1 * *

    (0 .0 0 9 )

    1 .0 2 1 * *

    (0 .0 0 9 )

    1 .0 1 6 * *

    (0 .0 0 6 )

    1 .0 1 6 * *

    (0 .0 0 6 )

    1 .0 1 3 * *

    (0 .0 0 5 )

    1 .0 1 3 * *

    (0 .0 0 5 )

    P re -t re n d

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    P o st -t re n d

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 *

    \ 0 .0 0 1

    1 .0 0 0

    \ 0 .0 0 1

    1 .0 0 0 * * *

    \ 0 .0 0 1

    1 .0 0 0 *

    \ 0 .0 0 1

    J Quant Criminol (2018) 34:741–773 759

    123

    T a b le

    6 co n ti n u ed

    W in d o w

    A ro u n d C u to ff

    6 -m

    o n th

    1 -y ea r

    2 -y ea r

    3 -y ea r

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    D ru g

    N o n d ru g

    S ta te

    fi x ed

    ef fe ct s

    1 .0 1 3

    0 .9 7 8

    0 .9 9 6

    0 .9 9 7

    0 .9 7 6

    0 .9 9 8

    0 .9 6 7 * *

    0 .9 8 5 *

    N 1 2 9 ,2 7 3

    2 6 2 ,7 3 6

    5 1 8 ,7 9 1

    7 6 7 ,0 5 9

    E st im

    at ed

    D iD

    B an

    Im p ac t (D )

    0 .0 3 6

    – 0 .0 0 1

    – 0 .0 2 2

    – 0 .0 1 8

    0 .0 3 4

    0 .0 2 4

    0 .0 1 7

    0 .0 1 4

    T h is ta b le re p o rt s co ef fi ci en ts as

    d es cr ib ed

    in E q s. (4 )– (6 ), co n v er te d in to

    h az ar d ra ti o s. S ta n d ar d er ro rs ar e re p o rt ed

    in p ar en th es es . S ta rs d en o te p v al u es

    fo r st at is ti ca l te st s o f

    d if fe re n ce s fr o m

    ze ro : * in d ic at es

    a v al u e o f 0 .0 5 ; * * in d ic at es

    a v al u e o f 0 .0 1 ; * * * in d ic at es

    a v al u e o f 0 .0 0 1 . N u m b er s ar e su b je ct

    to ro u n d in g er ro r

    760 J Quant Criminol (2018) 34:741–773

    123

    convenient shorthand to assess differences in recidivism among these ‘‘selected sample’’

    periods. Based on the depictions for Florida and Minnesota, we argue that the impact of

    sample selection appears to be minimal.14 We conclude that the potential for significant

    bias in this case is negligible and that our use of a linear trend in pre-periods is a likely

    sufficient control.

    Results

    Graphical Analyses

    As described earlier, we conducted graphical analyses in advance of formal estimation for

    the pooled sample as well as for each state. Because the output is lengthy, we present only

    the results for the pooled sample in the main body of the paper; however, full results are

    available in the ‘‘Appendix’’. Figure 1 shows illustrations for the pooled sample. Figures in

    the ‘‘Appendix’’ are identically constructed.

    Figure 1 shows four graphs. All four graphs depict changes in recidivism, centered on

    the timing of (conviction around) the initial ban. The x-axis of each graph denotes the

    month of the prison admission and the y-axis denotes the percent of offenders returning to

    prison within a 3-year period after release. For each set of illustrations, the top two

    illustrations show changes for men and the bottom two show changes for women.

    Table 7 Estimated impacts of the initial ban

    Women Men

    6-month 1-year 2-year 3-year 6-month 1-year 2-year 3-year

    CA -0.200 -0.135 -0.059 -0.081 -0.013 -0.058 -0.059* -0.054**

    0.130 0.091 0.064 0.053 0.047 0.033 0.023 0.019

    FL 0.553 0.254 -0.013 -0.122 0.099 0.159 0.194* 0.179

    0.358 0.331 0.404 0.524 0.098 0.084 0.086 0.095

    GA 0.636 0.196 0.049 0.212 0.007 -0.061 -0.077 -0.090

    0.414 0.279 0.193 0.157 0.120 0.084 0.059 0.048

    IL 0.142 0.134 0.020 -0.226 0.127 0.053 0.006 0.072

    0.239 0.170 0.118 0.180 0.076 0.054 0.038 0.048

    MI 1.099 0.862 0.501 0.237 -0.135 -0.096 -0.096 -0.102

    0.757 0.493 0.331 0.265 0.190 0.129 0.090 0.074

    MN 1.069 -0.019 0.158 0.543 -0.400 -0.212 -0.093 -0.303

    1.187 0.732 0.489 1.23 0.303 0.210 0.150 0.192

    State-average 0.550 0.215 0.109 0.116 -0.053 -0.036 -0.065 -0.038

    0.627 0.409 0.307 0.565 0.163 0.115 0.085 0.097

    This table reports DiD estimates described in Eq. (3) as differences in hazard ratios. Standard errors are reported in parentheses. Stars denote p values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value of 0.01; *** indicates a value of 0.001. Numbers are subject to rounding error

    14 We also conducted empirical tests of impacts excluding Florida and Minnesota. Results from these tests did not change the core findings of this paper.

    J Quant Criminol (2018) 34:741–773 761

    123

    Illustrations on the left show changes for drug offenders and those on the right show

    changes for nondrug offenders.

    Each graph contains two sets of data points (diamond plots and triangle plots) and linear

    trend lines on either side of the discontinuity for visualization. Comparisons at the dis-

    continuities (i.e., first differences s and q) are derived from shift in these trends at (x = 0). Measures of the impact (i.e., second differences Ds and Dq) are derived from differencing the changes between rows (the top row reports results for drug offenders subject to the bans

    and the bottom row reports results for nondrug offenders).

    Figure 1 shows some interesting patterns. For male drug offenders (top left), a casual

    interpretation of this picture is that, relative to nondrug offenders (top right), the ban may

    have caused a small (but perhaps significant) decrease in the rate of 3-year recidivism.

    However, the picture also shows that a linear trend does not necessarily provide the best fit

    for these data. Changes over the interval between (±) 18 months recidivism remain flat;

    changes on the ends ([18 months and\-18 months) appear to drive the slope of the line. A quadratic estimation of the trend (on the left and right) provides a better visual

    approximation of the data and a near equivalent statistical fit.15 Under that specification,

    the apparent impact of the ban (as a decrease in recidivism around the discontinuity) all but

    disappears.

    For women, rate of recidivism over this entire period is more variable and shows

    arguably little to no change, especially for nondrug offenders. There do not seem to be any

    discernable differences in patterns of change between drug and nondrug groups across pre-

    and post-ban periods.

    Similar graphs for individual states (depicting data summarized monthly rather than

    weekly, shown in the ‘‘Appendix’’) also show consistent patterns of no effect either

    obvious or systematic. Patterns of recidivism between pre and post periods appear to

    Pooled Sample (Men) NondrugDrug

    Pooled Sample (Women) NondrugDrug

    0.14

    0.16

    0.18

    0.2

    0.22

    0.24

    0.26

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or tio

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    0.14

    0.16

    0.18

    0.2

    0.22

    0.24

    0.26

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or tio

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    0.1 0.12 0.14 0.16 0.18 0.2

    0.22 0.24

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or tio

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0.1 0.12 0.14 0.16 0.18 0.2

    0.22 0.24

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or tio

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    Fig. 1 Illustrations of the proportion drug and nondrug offenders returning to prison within 3 years of release, based on prison admission date centered at Aug 22, 1996

    15 The difference in the sum of the squared residuals between these competing trends is\0.0001.

    762 J Quant Criminol (2018) 34:741–773

    123

    unfold similarly for drug and nondrug offenders and for men and women. In sum, it

    appears that the introduction of the ban did not have a substantive impact on rates of

    recidivism for drug offenders either absolutely, or relative to nondrug offenders.

    Estimated Impact of the Initial Ban

    Tables 5 and 6 summarize the main results of our estimations for women and men

    respectively. Each table reports results from the full set of regressions for the pooled

    sample including estimated coefficients for individual- and county-level control variables

    as well as estimates of sd, snd and Ds described in Eqs. (1)–(3). For ease of interpretation, estimated coefficients have been converted to hazard ratios. Standard errors and statistical

    significant (based on p-values) are also reported in these tables.

    Overall these tables show that there is no strong evidence to support the hypothesis that

    the restriction or denial of benefits for drug offenders, male or female, has led to material

    impacts in the rate at which offending populations are returning to prison overall. Among

    women drug offenders (in Table 5), the change in relative risk attributable to the ban is

    between 0.01 and -0.04. For nondrug offenders estimates are similarly small, between

    0.01 and -0.01. Both sets of estimates are robust to the use of both small and large samples

    around the cutoff and arguably quite stable. Finally, point estimates of the DiD estimator

    (the last row in each table) show that estimated differences in the ban’s impact across

    groups are not statistically different from zero (between 0.02 and-0.03) for any of the four

    samples tested.

    Table 6 shows results for men. It shows that among male drug offenders, the estimated

    change in relative risk after the ban is between 0.01 and -0.03. For nondrug offenders

    estimates are between 0.00 and -0.02. As with women, DiD estimates are quite small

    (between, 0.04 and -0.02) and no estimates are statistically different from zero.

    Finally, given that states themselves are quite heterogeneous in terms of their policies

    and practices governing correctional populations, we separately estimate and report

    impacts for individual states. Table 7 summarizes the results of these estimations. Like

    Tables 5 and 6, Table 7 reports the DiD estimates from each exercise and for multiple

    samples. It does not report coefficients estimated from individual covariates.16

    Overall, Table 7 shows results that are consistent with the general findings from the

    pooled sample. Where samples are small, estimates are highly variable and no consistent

    findings emerge. Where samples are large, estimates are generally much closer to zero and

    most states do not show statistically or substantively significant impacts on recidivism.

    Some exceptions do exist, primarily in California where the largest sample shows a -0.054

    decrease in the relative risk for male drug offenders as compared to nondrug offenders.

    Additional Tests of the Impact

    In addition to the main results above, we conducted additional tests to provide greater

    context for the results. First, we explored possible associations between the time spent at

    risk and the impact of restricting benefits. Specifically, we tested whether the ban’s impact

    varies over time-at-risk by separately estimating the average impact of the ban over various

    segments: (1) during the first 6 months following release, (2) between 6 and 18 months

    following release, and (3) more than 18 months following release.

    16 Results are available upon request.

    J Quant Criminol (2018) 34:741–773 763

    123

    Given that the risk of returning to prison naturally diminishes over time (Langen and

    Levin 2002; Durose et al. 2014), it may be that denying benefits has the greatest impact

    early in the re-entry period. On the other hand, it may be that benefits impact an offender’s

    ability to address more long-term challenges, especially if it takes time for offenders to

    begin receiving benefits. If so, then denying benefits may imply consequences later in the

    re-entry period. In either case, significant, heterogeneous impacts may exist even where the

    average effect implied is not different from zero.

    Table 8 reports DiD estimates of the ban’s impact over time-at-risk and across sampling

    windows, using the pooled sample only. Overall this table suggests some provocative

    patterns. For both men and women, point estimates of impacts on the relative risk for drug

    offenders are negative in the first six months after release, though for women, these

    estimates are not statistically different from zero. However, after 18 months following

    release, these patterns reverse—point estimates for both men and women are most often

    positive, suggesting recidivism worsens for drug offenders during this period. Again these

    patterns are not statistically different from zero; however, they suggest a real possibility

    that impacts are heterogeneous over time.

    From a behavioral perspective, it may not be unreasonable to expect that denying SNAP

    and TANF benefits has differential impacts in the short run vs. the long run. Consider the

    following example. If the fear of losing social supports causes short-run behaviors (e.g.,

    more aggressive job searching) among risky offenders to change, the near-term impact of

    the ban may be beneficial (i.e., by reducing recidivism). At the same time, if the long-term

    loss of support among less risky offenders creates ongoing hardship, then the net effect

    over the long term may be detrimental (i.e., by increasing recidivism).

    Results from this table do not validate such stories; however, they do provide an

    impetus for further investigation. Given the inherent limitations in our ITT analysis, we

    argue that the results from this table are best interpreted as an exploratory exercise and that

    future investigation should consider the possibility, nature, and causes of heterogeneous

    impacts of the ban’s application.

    We performed a second exploratory test of impacts to examine whether there is any

    evidence to suggest that our null finding (an ITT estimate) would be nonzero if it were

    estimated as a TOT estimate. This test exploits county-level variation in SNAP partici-

    pation (as measured in 1995) to compare impacts, but requires two strong (and untestable)

    assumptions. The first assumption is that offenders coming from counties with higher rates

    of SNAP participation are themselves more likely to be SNAP/TANF recipients. If

    Table 8 Estimated impacts of the initial ban

    Women Men

    6-month 1-year 2-year 3-year 6-month 1-year 2-year 3-year

    0–6 Months -0.046 0.010 -0.010 -0.103 -0.017 -0.076* -0.085*** -0.101***

    0.135 0.093 0.067 0.056 0.046 0.032 0.023 0.019

    6–18 Months -0.065 -0.030 -0.009 -0.031 0.075 0.020 -0.022 -0.008

    0.124 0.087 0.061 0.050 0.042 0.029 0.021 0.017

    18? Months 0.113 -0.024 0.038 0.027 0.042 0.040 0.029 0.037*

    0.122 0.086 0.061 0.050 0.040 0.028 0.020 0.016

    This table reports DiD estimates described in Eq. (3) as differences in hazard ratios. Standard errors are reported in parentheses. Stars denote p values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value of 0.01; *** indicates a value of 0.001. Numbers are subject to rounding error

    764 J Quant Criminol (2018) 34:741–773

    123

    offenders coming from high-participation areas are more often themselves recipients of

    SNAP and/or TANF, then ITT estimates in counties with higher participation come closer

    to TOT estimates while ITT estimates in low-participation areas are more biased toward

    zero, since these areas include a higher proportion of noneligible nonparticipants. We

    looked to see if any such patterns exist.

    This test requires information about each offender’s county of residence; however, the

    NCRP does not currently report this information. Instead we relied on the reported county

    of conviction (an available measure) as a proxy for residence. Thus our test requires a

    second assumption—offenders are likely to be convicted in the counties in which they

    reside. While there is no test for this in the NCRP data, there is a known body of literature

    that supports the argument that offenders often commit crimes near the communities where

    they live (e.g., Eck and Weisburd 2015; Cohen and Felson 1979; Brantingham and

    Brantingham 1993, 1995).

    Based on these conditions, we examined whether estimated impacts in high-SNAP

    concentration counties are larger than in low-concentration counties. Specifically, esti-

    mates from the pooled regression are grouped into deciles, so that the lowest decile (the

    1st) represents the 10% of counties with the lowest proportion of SNAP households (\6% of households), and the highest decile (the 10th) represents the 10% of counties with the

    highest proportion ([30% of households). Results are reported in Fig. 2. Figure 2 shows the estimated (DiD) impact of the drug felony ban, by SNAP household

    concentration, for both men and women using the 3-year sample (results are not sensitive to

    our sample selection). Overall this figure shows that among bothmen andwomen there are no

    discernable patterns of differences in impacts across counties. In terms ofmagnitude, average

    impacts among the bottom 20% of counties are\0.01 different from the top 20% of counties. Overall, the test is weak but suggests no aggregate impacts resulting from the ban.

    The third test is a general sensitivity test of our results to alternative specifications that

    model time trends as higher-order polynomials rather than simple linear trends. Specifi-

    cally, we tested a quadratic and third-order specification of time trends in addition to the

    linear arguments shown in earlier regression equations (i.e., three specifications). We did

    this because more flexible time trends can provide better fits to the data, though some

    -0.5

    -0.4

    -0.3

    -0.2

    -0.1

    0

    0.1

    0.2

    0.3

    0.4

    1st 2nd 3rd 4th 5th 6th 7th 8th 9th 10th 1st 2nd 3rd 4th 5th 6th 7th 8th 9th 10th

    Av er

    ag e

    (D iD

    ) E st

    im at

    es

    Women Men

    Fig. 2 Average (DiD) Ban impacts across counties in the pooled sample, by SNAP household concentration and sex

    J Quant Criminol (2018) 34:741–773 765

    123

    literature also argues that higher-order approximations run a greater risk of introducing

    bias (Gelman and Imbens 2014).

    Overall we find that our main results are extremely robust to these alternative specifi-

    cations. Of the 56 additional tests we conducted for men (across pooled and state samples),

    1 test (2%) yielded significant DiD estimates at a p value\0.05. For women, 56 additional tests yielded 2 significant DiD estimates (4% of tests) at a p value\0.05. Given that with so many tests we would expect at least some findings by chance even where no true effects

    exist, these results reinforce the main finding of no effect.

    Finally we tested the sensitivity of our results to our use of the Cox model. While the Cox

    model allows for flexible estimation of the hazard function, it requires a strong assumption

    about the proportionality of hazards across measures. By contrast, a less flexible parametric

    survival model does not impose proportionality. As such, we compared our results from the

    Cox estimation to a similarly estimated set of parametric survival models that impose a

    gamma distribution for the survival function. In cases where the model under a gamma

    distribution could not be estimated, we substituted aWeibull distribution instead. Overall we

    found that our conclusions are robust to the use of this alternative specification.

    Discussion

    For the last 20 years, most states have imposed some form of special restrictions on drug

    felons seeking SNAP and TANF benefits. It seems now though that the social and political

    tone of the public conversation is at a critical point. Nearly half a century of steady and

    persistent prison population growth is forcing lawmakers to reconsider the merits of long-

    standing policies, including the drug felony ban. And despite the political rhetoric, there

    have been no confirmatory tests of whether and how manifestations of these laws have

    resulted in tangible differences to prison systems. Without that evidence, it is impossible

    for policymakers to understand the consequences of actions taken to expand or reduce

    access to benefits for offenders.

    This paper uses a rigorous quasi-experimental approach together with longitudinal

    prison data and state data on ban adoptions to test competing theories. Results of this

    analysis are conclusive: neither the denial nor the expansion of SNAP or TANF benefits to

    drug offenders will adversely or positively impact the size of drug offender populations in

    state prisons. These results appear to extend to both men and women and to all observed

    variations of state policies.

    The obvious question stemming from this analysis is: ‘‘Why don’t welfare laws seem to

    matter in this context?’’ There are several potential answers. First, it may be that there are

    too few offenders receiving benefits to substantively impact prisons and that low rates of

    recipiency are masking true impacts at the individual level. Our ITT framework is infor-

    mative, but it does not identify impacts for the subset of eligible offenders.

    Second, it may be true that the benefits denied to drug offenders under these laws simply

    are not significant enough to differentially impact recidivism in a meaningful way. Con-

    sider, for example, that the disqualification of an individual from TANF does not disqualify

    the entire household from benefits. In cases where a drug felon’s household continues to

    receive benefits, the ban acts to reduce, but not eliminate, benefits. These partial household

    benefits mitigate the denial of benefits to the individual. Similarly, the PRWORA does not

    ban drug felons from receiving nonassistance benefits from TANF, including many benefits

    that we might consider critical to successful re-entry, e.g., services such as counseling, job

    766 J Quant Criminol (2018) 34:741–773

    123

    retention and employment-related services that do not provide basic income support. To

    the extent that these services have an impact, the ban has less overall influence.

    Another possibility is that true heterogeneous impacts among offender subgroups are

    not observed when estimating the local average treatment effect. We partly explore this

    possibility in the paper; however, other unexplored offender subgroups may provide

    additional context. For example, it may be that the impact of the ban is heterogeneous with

    respect to an offenders’ age, race or family size. A deeper examination of possible

    heterogeneity may reveal new insights.

    There are other limitations to our analysis which have implications for the impacts we

    estimate, some of which might be addressed in the future with improvements to the data or

    extensions of analyses. For example, identification of offenders in the data is not error-free

    and has implications for analysis. First, although most offenders in prisons are felons,

    NCRP data do not allow us to separate misdemeanants from felons and control for them in

    analysis. To the extent that misdemeanants are part of the sample, impact estimates are

    biased toward a null finding.

    Second, our labeling of offenders as drug or nondrug offenders is not perfect. Since we

    cannot observe every offender’s complete incarceration history in every state, we cannot

    avoid misclassifying at least some drug offenders as nondrug offenders. Third, our iden-

    tification of new crimes based on prison admission codes is imperfect. Discretion in the

    judicial process and variable sentencing structures across states obscure the meaning of

    these codes (Gaes et al. 2016).17 Within the constraints of the NCRP, there may be no

    solution to this problem; however, the integration of new information such as arrest records

    may help resolve the issue. Similarly, discretion and uncertainty in the use and application

    of charging offenses makes a more granular investigation of patterns in outcomes relatively

    uninformative. Arrests records may provide illumination.

    Finally, one area that future investigators should explore more closely is whether and how

    ban modifications have impacted offender outcomes such as recidivism. The identification

    strategy we present in this paper is not adequate for such an investigation. Credible estimates

    require more first-hand knowledge (and data) about real-world implementation of modified

    policies and practices. For example, it is important to know whether offenders released prior

    to the ban’s modification retrospectively seek out benefits for which they have become

    eligible. Do state agencies actively pursue such cases? How? Answers to such questions are

    critical to proper sample selection. We leave this exercise to future research.

    Overall, there is no doubt that this analysis answers important questions. Will ban

    removal help to alleviate the problem of mass incarceration? The answer appears to be no.

    Is there a behavioral basis for denying benefits to drug offenders while providing benefits

    to nondrug offenders and violent offenders? The answer again appears to be no. However,

    the answers to these questions also inspire other, yet unresolved questions. What should

    states do next? Should ban removal be encouraged or discouraged? The answers to these

    questions are subject to debate; however, that debate should be informed by future research

    that more closely examines how individuals are directly impacted by the receipt of welfare.

    Fortunately, BJS is at present undertaking an effort to expand the use of NCRP records by

    merging them with other offender-level information including welfare use. Use of new data

    from that effort will undoubtedly lead to novel insights along this line of inquiry.

    17 This paper proposes one alternative construction for a ‘‘new crime’’ using a time-based rule that classifies all prison admissions as new crimes when no release from prison has been observed within the prior year. We test the sensitivity of our results to this classification rule (as well as a 3-year variant of this rule) and find no discernable difference in our findings.

    J Quant Criminol (2018) 34:741–773 767

    123

    Acknowledgements This work was supported by Grant Nos. 2010-BJ-CX-K067 and 2015-R2-CX-K135 awarded by the Bureau of Justice Statistics, Office of Justice Programs, US Department of Justice. For this work, Thomas Rich served as Project Director along with Principal Investigators William Rhodes and Gerry Gaes. Points of view in this document are those of the authors and do not represent the official position of the US Department of Justice. The authors are responsible for any errors in the paper.

    Appendix

    See Fig. 3.

    CALIFORNIA Pooled Sample (Men)

    Drug Nondrug

    Pooled Sample (Women) Drug Nondrug

    0.1

    0.15

    0.2

    0.25

    0.3

    0.35

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0.1

    0.15

    0.2

    0.25

    0.3

    0.35

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0.1

    0.15

    0.2

    0.25

    0.3

    0.35

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0.1

    0.15

    0.2

    0.25

    0.3

    0.35

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36

    Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    FLORIDA Pooled Sample (Men) Drug Nondrug

    Pooled Sample (Women) Drug Nondrug

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    Fig. 3 State-by-state illustrations of the proportion drug and nondrug offenders returning to prison within 3 years of release, based on prison admission date centered at Aug 22, 1996

    768 J Quant Criminol (2018) 34:741–773

    123

    GEORGIA Pooled Sample (Men) Drug Nondrug

    Pooled Sample (Women) Drug Nondrug

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -40 -20 0 20 40 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    ILLINOIS Pooled Sample (Men)

    Drug Nondrug

    Pooled Sample (Women) Drug Nondrug

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in

    3 Ye

    ar s

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    0

    0.05

    0.1

    0.15

    0.2

    0.25

    -36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban

    Pr op

    or �o

    n Re

    tu rn

    in g

    w ith

    in 3

    Y ea

    rs

    Fig. 3 continued

    J Quant Criminol (2018) 34:741–773 769

    123

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    Reproduced with permission of copyright owner. Further reproduction prohibited without permission.

    • A Quasi-Experimental Evaluation of the Impact of Public Assistance on Prisoner Recidivism
      • Abstract
        • Introduction
        • Objective
        • Methods
        • Results
        • Conclusion
      • Introduction
      • Background
        • Offender Re-Entry, Economic Challenges and Use of Welfare
        • SNAP, TANF and Recidivism: The Potential Impact of Denying Benefits
        • Using the Ban as a Natural Experiment for Denying Benefits
        • State Implementation of the Drug Felony Ban
      • Data
      • Method
      • Results
        • Graphical Analyses
        • Estimated Impact of the Initial Ban
        • Additional Tests of the Impact
      • Discussion
      • Acknowledgements
      • Appendix
      • References

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